Correcting Residual Errors With Spectral, Ultrasound, Traditional Speech Therapy: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Correcting Residual Errors With Spectral, Ultrasound, Traditional Speech Therapy (NCT03737318), a randomized na study. The primary outcome is Change in F3-F2 Distance (Hz) Across Sessions, Measured From /r/ Sounds Produced in Syllables or Words During Practice..

2. Clinical Question

3. Trial Design

The registry describes a completed, randomized, single-masked, parallel-group behavioral trial. Enrollment was 108. Participants were assigned to traditional articulation treatment, visual-acoustic biofeedback, or ultrasound biofeedback. The record does not describe the randomization procedure, allocation concealment, or which people were masked.

The primary outcome was assessed during Phase I, consisting of three 90-min sessions over ~1 week. It concerns the change in F3-F2 distance from Session 1 to Session 3, based on /r/ sounds produced in syllables or words during practice. Three participants in the visual-acoustic group could not be acoustically analyzed because of poor audio quality. The arm-level primary-outcome counts reported are 45 for traditional treatment, 29 for visual-acoustic biofeedback, and 31 for ultrasound biofeedback.

Two additional outcomes were posted. One measured change from before treatment to after all treatment, described as ~10 weeks later, in the percentage of word-probe /r/ sounds rated correct by untrained listeners. The other was a parent survey about the impact of the speech disorder on social, emotional, and academic well-being, also assessed before and after treatment. The record does not give further details about the full treatment schedule or the survey scale’s interpretation.

The study status is completed. The registry lists a start date of 2019-03-01 and a primary completion date of 2024-08-31. The trial’s original sample-size justification, detailed protocol, and planned statistical analysis are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Phase 1 (Acquisition)

Phase 2 (Generalization)

Reasons for not completing this period:

Analysis population for the primary outcome, as defined in the registry: Three participants from group 2 (visual-acoustic biofeedback) could not be acoustically analyzed due to poor audio quality.

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change in F3-F2 Distance (Hz) Across Sessions, Measured From /r/ Sounds Produced in Syllables or Words During Practice., measured over Phase I: three 90-min treatment sessions delivered over ~1 week; reported value is the change from Session 1 to Session 3 (slope across sessions).

The primary endpoint is change in F3-F2 distance, measured in Hertz, across treatment sessions. F3-F2 is an acoustic measure of the difference between two formant frequencies in a child’s /r/ sound. The registry explains that smaller distances indicate a sound closer to a typical adult-like /r/, while larger distances indicate a more distorted sound. It also describes a typical-peer reference of roughly ~500 Hz and distorted /r/ values often >1000 Hz. Those descriptions provide context for the acoustic measure, not a threshold for judging an individual participant.

The posted endpoint is not simply a single rating of speech quality. It is described as a model-based estimate of change from Session 1 to Session 3, or the slope across sessions, for productions during practice. In the endpoint description, a more negative change indicates greater improvement. Because the measure is continuous, its mean can summarize the group’s average value, while its standard deviation describes variation among observations.

General: using a repeated acoustic measure can capture how speech production changes during a short treatment phase, rather than relying only on a before-and-after assessment. The measure is also more specific than a broad impression of intelligibility: it quantifies an acoustic feature associated with /r/ accuracy. Its interpretation depends on the direction and definition of the modeled change, the quality of the recordings, and the statistical model. The registry record does not provide the complete model specification or details of how all repeated observations were handled.

7. Results Posted in the Registry

• Group 2: Biofeedback--visual-acoustic: mean 66.70 versus 38.20 on control; difference 28.50 (95% CI -13.66 to 70.66), standardized effect d = 0.35; z-test p = 0.185.
• Group 3: Biofeedback-Ultrasound: mean 85.20 versus 38.20 on control; difference 47.00 (95% CI -9.88 to 103.88), standardized effect d = 0.43; z-test p = 0.105.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change From Pre to Post in Percent "Correct" Ratings by Untrained Listeners, for /r/ Sounds Produced in Word Probes.

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Group 2: Biofeedback--visual-acoustic: mean 43.20 versus 44.50 on control; difference -1.30 (95% CI -17.04 to 14.44), standardized effect d = -0.04; z-test p = 0.871.
  • Group 3: Biofeedback-Ultrasound: mean 49.60 versus 44.50 on control; difference 5.10 (95% CI -11.07 to 21.27), standardized effect d = 0.15; z-test p = 0.536.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 2: Biofeedback--visual-acoustic and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 3: Biofeedback-Ultrasound and the control. The interval gives the range of effects that remain compatible with the data.

Impact of Speech Disorder on Social, Emotional, and Academic Well-being (Parent Survey)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Group 2: Biofeedback--visual-acoustic: mean 1.90 versus 1.90 on control; difference 0.00 (95% CI -0.51 to 0.51), standardized effect d = 0.00; z-test p = 1.000.
  • Group 3: Biofeedback-Ultrasound: mean 2.10 versus 1.90 on control; difference 0.20 (95% CI -0.35 to 0.75), standardized effect d = 0.17; z-test p = 0.473.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 2: Biofeedback--visual-acoustic and the control. The interval gives the range of effects that remain compatible with the data.
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Group 3: Biofeedback-Ultrasound and the control. The interval gives the range of effects that remain compatible with the data.

The two secondary outcomes assess different domains from the primary acoustic measure. One concerns the change in the percentage of /r/ word probes judged correct by untrained listeners; the other concerns parent-reported social, emotional, and academic impact. The registry reports a treatment-by-time interaction for each, with different statistical patterns: the listener-rating analysis has a small p-value, while the parent-survey analysis does not. The arm-level summaries and recalculated comparisons also do not present one consistent pattern across both outcomes.

This mix of findings is not inherently contradictory. The primary measure is an acoustic feature recorded during practice over Phase I, whereas untrained-listener ratings reflect judgments of word probes before and after treatment, and the parent survey captures perceived impact. Measures may differ in what they assess, when they are collected, their variability, and how sensitive they are to change. Agreement across measures is not guaranteed.

The secondary analyses can add context to the primary result, but they cannot by themselves confirm or overturn the acoustic interaction. Their findings should be interpreted as evidence about their own outcomes and timeframes, not as direct proof of the primary endpoint’s clinical meaning.

Unadjusted secondary results carry less weight when several outcomes or comparisons are considered because repeated testing increases the chance of obtaining an apparently notable result by chance. General: multiplicity procedures can control error rates across a family of tests, but the registry record does not report whether such a procedure was planned or applied. The sponsor’s secondary interaction analyses are reported, but a full prespecified hierarchy or adjustment strategy is not reported in the registry record. These secondary findings are therefore useful context, while warranting caution about isolated statistical signals.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Change From Pre to Post in Percent "Correct" Ratings by Untrained Listeners, for /r/ Sounds Produced in Word Probes.
• Impact of Speech Disorder on Social, Emotional, and Academic Well-being (Parent Survey)

9. Statistical Interpretation

10. Statistical Methods Explained

General: a randomized parallel-group design assigns participants to different intervention groups and compares outcomes across those groups. Random assignment is intended to reduce systematic differences at the start of a trial, but the registry record does not state how the sequence was generated or concealed. It reports single masking without identifying who was masked. Those missing details limit assessment of how allocation and masking were implemented.

What does the primary model estimate?

The sponsor reports a linear regression treatment-by-time interaction. In general, a treatment-by-time interaction tests whether the pattern of change over time differs across treatment groups. The reported coefficient is 106.41, its 95% confidence interval is 63.06 to 149.76, and p < .0001. The registry record does not identify the time coding, reference group coding, covariates, correlation structure, or other parts of the fitted model. Without those details, the coefficient cannot be translated confidently into a particular group’s change or a direct contrast between each biofeedback intervention and traditional treatment.

General: regression can account for the structure of an outcome and estimate a conditional association under the model’s assumptions. The validity of a regression estimate depends on how the outcome, time, treatment groups, and repeated observations are represented. A confidence interval describes uncertainty around the estimated coefficient under the fitted analysis; it does not address every possible source of bias or model misspecification.

How do the recalculations differ?

The arm-level summaries give means and standard deviations for each group. Simple recalculations compare the biofeedback group mean with the traditional-treatment group mean, without adjustment. These are not the same as the sponsor’s treatment-by-time regression interaction. A difference between these summaries can arise because they represent different estimands or use different modeling and data-handling choices. The registry flags a discrepancy, and the sponsor’s own analysis takes precedence. The record does not explain the discrepancy sufficiently to attribute it to a specific cause.

General: an unadjusted mean difference describes the difference between two group averages. Its confidence interval reflects sampling uncertainty under the simple comparison, but does not incorporate model adjustments or repeated-measure structure that may be part of a regression analysis. A p-value from such a recalculation is not interchangeable with the p-value for a different model parameter. The recalculated comparisons should therefore be treated as descriptive checks, not as a replacement for the registered sponsor analysis.

Why do repeated measurements matter?

The primary outcome is defined as change across sessions, with measurements from Session 1 to Session 3. Repeated measurements on the same participant are generally correlated: observations from one person tend to be more alike than observations from different people. General: a model for repeated measurements should account for that dependence, since treating all observations as unrelated can misstate uncertainty. The registry identifies a linear regression interaction for the reported analysis, but does not describe the repeated-measure covariance structure, whether participant-level clustering was used, or how the model handled incomplete session data.

The endpoint description says the sponsor’s estimate is model-based and refers to change across sessions as a slope. A slope uses the pattern across time points to express the rate or direction of change. The posted value is not described as a raw within-person difference for every participant. Exact modeling details are not reported in the registry record, so the estimate should be interpreted at the level of the stated treatment-by-time interaction.

What do the standard deviations and confidence intervals represent?

The arm summaries report means and standard deviations. General: a standard deviation describes how dispersed individual observations are around a group mean; it is not the uncertainty of the mean itself. A confidence interval for a contrast or model coefficient expresses uncertainty about that estimated quantity. The intervals for the sponsor’s regression analysis and the simple mean recalculations refer to different quantities, so they should not be compared as though they were estimates from one identical procedure.

The three participants without acoustically analyzable recordings in the visual-acoustic group are specifically noted for the primary outcome. The registry record does not report whether other participants had missing outcome measurements, how missing observations were handled, or whether an imputation method was used. It also does not state whether the reported analysis followed intention-to-treat, per-protocol, or another population definition.

What role do p-values play?

General: a p-value measures how incompatible the observed data are with a specified null hypothesis under the statistical model. It is not the probability that the null hypothesis is true, and it does not measure the size or practical importance of an effect. The primary sponsor analysis reports p < .0001. That value is evidence against the model’s null hypothesis for the reported interaction, but it does not by itself explain the coefficient’s meaning, establish the importance of the change, or resolve the noted discrepancy with the unadjusted recalculations.

The sponsor identifies the reported analysis type as superiority. That label describes the analysis framework, but the record does not report the complete prespecified statistical plan, multiplicity strategy, or a protocol-based interpretation threshold. The trial’s original sample-size justification and planned interim analyses are not reported in the registry record. No claim about those design features can be made from the posted statistical summaries alone.

Why can variability complicate interpretation?

General: when observations vary substantially within groups, estimated differences are less precise unless the analysis or design provides additional information. Here the arm summaries include standard deviations, but the registry does not describe whether the outcome distribution was checked, whether influential observations were assessed, or what sensitivity analyses were conducted. These omissions do not prove that the model is inappropriate; they mean the available record cannot be used to assess those checks.

11. Confidence Intervals and Precision

The sponsor’s primary regression estimate is 106.41, with a 95% confidence interval from 63.06 to 149.76. This interval gives a range of values compatible with the fitted model and data under the analysis assumptions. It excludes zero, consistent with the reported p < .0001 for the interaction. The interval’s width also matters: the estimate is not known with exact precision, and its interpretation depends on the model parameter’s coding and meaning.

The simple recalculations compare each biofeedback group’s posted mean with the traditional-treatment mean. Both recalculated confidence intervals include zero: the visual-acoustic comparison ranges from -13.66 to 70.66, and the ultrasound comparison ranges from -9.876 to 103.9. These intervals are unadjusted comparisons of means and should not be treated as the confidence intervals for the sponsor’s treatment-by-time interaction. Because the registry flags a discrepancy, the sponsor’s own analysis takes precedence.

General: a confidence interval is not a guarantee that the true value lies within its endpoints, nor does it express the probability that a particular treatment effect is correct. It describes statistical uncertainty under the method used. Precision depends on such features as the amount of information, variability, model structure, and missingness. The registry does not report enough detail about the model or missing data to evaluate all of these influences.

The endpoint also has an interpretive precision issue: the registry describes more negative change as greater improvement, while the reported sponsor coefficient is positive. The record does not explain the coefficient coding in enough detail to translate its sign into a straightforward direction of improvement. The interval can be read numerically as the uncertainty range for the reported coefficient, but not as a resolved, group-specific clinical contrast.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The sample-size entries are planning illustrations based on the observed effect, not the trial’s original sample-size calculation. The original design assumptions are not reported in the registry record. These planning figures assume a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation. Each planning row considers an effect defined as the stated fraction of the observed effect.

The columns for 80% power and 90% power describe the number of participants per arm in a hypothetical study under those assumptions. In plain terms, 80% power is the chance of detecting the specified effect at the stated significance level if that effect is real and the assumptions hold; the corresponding 90% column uses a higher target chance of detection. Greater target power generally requires more participants for the same effect. The figures are participants per arm, not total events.

Each comparison has its own planning illustrations because the observed differences and variability differ between comparisons. The rows that plan for a smaller fraction of the observed effect require more participants per arm. This reflects a general statistical principle: smaller effects are harder to distinguish from random variation, all else equal. The displayed values are planning scenarios rather than observed trial results.

These figures are not observed power. They are prospective illustrations using the observed effect as a starting point, and they do not establish whether the trial was adequately powered under its actual design. They also do not reproduce a full three-group repeated-measures analysis; the stated planning assumptions concern an equal-allocation comparison between two arms.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = 28.500; pooled standard deviation σ = 82.388.
2. n = 2 × (1.96 + 0.842)² × 82.388² / 28.500² = 131.2, rounded up to 132 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- 28.5                      # observed difference in means
sigma <- 82.3876339156686                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(3737318)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 132 (80% power), 176 (90% power)
 75% of observed effect: n per arm = 234 (80% power), 313 (90% power)
 50% of observed effect: n per arm = 525 (80% power), 703 (90% power)
power.t.test: 132.1 
Simulated power at n = 132 per arm: 0.803 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The sponsor’s own analysis is a linear regression treatment-by-time interaction across the three groups. It reports an estimate of 106.41, a 95% confidence interval from 63.06 to 149.76, and p < .0001. This is the analysis reported in the registry and is the primary basis for describing the sponsor’s result.

The recalculated comparisons use posted arm-level means and standard deviations to form simple, unadjusted comparisons of each biofeedback group with traditional treatment. Those calculations do not reproduce the sponsor’s regression model or necessarily estimate the same quantity. The registry flags a discrepancy between the sponsor result and the recalculated values. In that circumstance, the sponsor’s own analysis takes precedence; the recalculations are best treated as limited descriptive checks and not as corrections to the registered analysis.

The record does not explain exactly why the estimates differ. It does not provide enough detail to determine whether the difference reflects distinct estimands, modeling choices, data included, or another issue. The endpoint description also says that more negative change indicates greater improvement, while the reported interaction coefficient is positive. Without the model’s coding details, the coefficient’s direction cannot be translated into a direct statement about which group improved more. The coefficient and recalculated mean contrasts should therefore remain clearly distinguished.

15. Multiplicity, Missing Data and Analysis Populations

The registry posts a primary outcome and two secondary outcomes, with sponsor-reported regression analyses. It does not report whether the statistical plan specified a hierarchy among outcomes, whether the primary analysis had a single designated contrast, or whether p-values were adjusted for multiple outcomes or comparisons. The presence of multiple analyses raises a general multiplicity concern: when many hypotheses are tested, the chance of at least one apparently notable result can increase. Without a reported correction strategy, the reader cannot determine how the analyses were intended to control that risk.

Important details about missing data are also absent. The record notes that three participants in the visual-acoustic group could not be acoustically analyzed because of poor audio quality. It does not describe whether those observations were excluded from all primary analyses, whether any other measurements were missing, or how missing values were handled. The posted primary arm counts do not by themselves establish the analysis population or explain why each participant was or was not included.

The registry record does not state whether the analysis followed an intention-to-treat population, a per-protocol population, or another definition. It also does not report a sensitivity analysis for missing data, model diagnostics, or the handling of departures from model assumptions. These omissions limit evaluation of how robust the results are to participant exclusions and analytic choices; they are not evidence that a particular approach was or was not used.

The original sample-size rationale, interim-analysis plan, and complete statistical analysis plan are not reported in the registry record. The planning illustrations based on observed effects are separate from those unreported original design decisions and cannot fill in those details.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Deaths

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

The registry reports zero serious adverse events and zero deaths in each of the three treatment groups. It also reports zero other adverse events in each group. The numbers at risk differ by group in the safety record: 45 for traditional articulation treatment, 32 for visual-acoustic biofeedback, and 31 for ultrasound biofeedback. These are the registry’s posted safety counts and should be read separately from the primary acoustic analysis counts.

These entries describe what was reported in the registry record. They do not provide information about the type of events actively monitored, the event-collection period, attribution to treatment, or how adverse events were solicited. No serious-event terms are listed. The absence of reported events in these entries should not be taken to establish that no possible adverse experience occurred; it means that the registry’s posted counts are zero for the listed categories.

17. What the Result Does, and Does Not, Mean

The posted results answer a statistical question about how outcomes changed across treatment groups under the analyses described in the registry. The primary sponsor analysis reports a treatment-by-time interaction, while the secondary outcomes assess listener judgments and parent-reported impact. These are different measurements, and their results should not be collapsed into a single claim about speech, everyday communication, or well-being.

The primary acoustic endpoint is a measure of F3-F2 distance in /r/ productions during practice. It is not itself a direct measure of how understandable a child is in daily conversation, of school or social functioning, or of long-term persistence of change. The listener-rating and parent-survey outcomes address different questions, and the posted results do not establish that changes in one measure necessarily lead to changes in another.

The sponsor-reported interaction is statistically distinct from the simple, unadjusted comparisons recalculated from group summaries. Because the registry identifies a discrepancy, the sponsor’s own analysis takes precedence. The available record does not fully describe the regression model’s coding or provide enough information to resolve the direction of the coefficient into a direct group-specific statement. The results should be read with that limitation in mind.

Statistical evidence from one completed trial does not, on its own, establish how an intervention will perform for every child or in other treatment settings. The posted summaries also do not establish the practical importance of a change, the durability of any observed change, or how treatment should be selected for an individual. No medical or treatment recommendation follows from these statistics alone.

General: statistical significance, effect magnitude, precision, measurement relevance, and study limitations are separate considerations. A small p-value does not automatically mean an effect is large or important, and a confidence interval does not capture every source of uncertainty. Here, interpretation is further constrained by the noted discrepancy and by unreported analysis details.

18. Why This Trial Matters Statistically

This trial is statistically informative because it compares traditional articulation treatment with two biofeedback approaches in a randomized, three-group design, while measuring /r/ production acoustically across treatment sessions. The primary endpoint is more specific than a broad clinical rating: it tracks a sound feature related to /r/ accuracy. The secondary measures also broaden the outcomes beyond acoustic practice data to listener judgments and parent-reported impact.

The record illustrates why a model-based result and a simple recalculation from group summaries should not automatically be treated as interchangeable. The sponsor’s analysis estimates a treatment-by-time interaction, whereas the unadjusted recalculations compare arm-level means. The registry flags a discrepancy, making clear that interpretation depends not only on the numbers but also on the estimand and analysis method. The sponsor’s own analysis takes precedence, while the unexplained discrepancy remains relevant context.

The trial also highlights the value of separating statistical evidence from measurement meaning. A clearly reported interaction and a small p-value do not, without model coding and clinical context, settle which group’s change is greater or how an acoustic difference translates into everyday speech. Different endpoints may capture different dimensions of change, and the secondary outcomes do not show a uniform pattern.

Finally, the record documents a practical measurement issue: some recordings in one group were not suitable for acoustic analysis. This underscores that outcome quality and missingness are part of the statistical interpretation, not merely technical details. The record does not provide enough information to assess all consequences of that issue, so transparent reporting of analysis populations and missing-data methods would be important for a fuller appraisal.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

The main trial-specific limitation for interpretation is the discrepancy flagged between the sponsor’s regression analysis and the unadjusted recalculations from arm summaries. The sponsor analysis takes precedence, but the record does not explain the discrepancy. The regression coefficient’s coding and reference structure are also not described in enough detail to translate its sign into a group-specific direction of improvement, particularly given the endpoint description that more negative change indicates greater improvement.

Three participants in the visual-acoustic group could not be acoustically analyzed because of poor audio quality. The record does not explain how those observations were handled in the sponsor analysis, whether other primary measurements were missing, or whether sensitivity analyses were performed. The reported analysis population is not described. These gaps limit assessment of potential effects of missing or excluded measurements.

The registry reports single masking but does not identify who was masked or explain how masking was implemented. The randomization method, allocation concealment, complete treatment schedule, model specification, model diagnostics, and use of covariates are not reported in the registry record. The original sample-size justification and interim-analysis plan are likewise not reported.

The primary outcome reflects acoustic performance during practice in Phase I, while the secondary measures use different assessments and timeframes. The registry does not provide enough information to establish the durability of change or translate acoustic values into everyday communication. Multiplicity handling across outcomes and comparisons is not reported, so the secondary results warrant caution. These limitations identify gaps in the posted record; they do not establish that the underlying study lacked procedures or analyses that were not described.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Correcting Residual Errors With Spectral, Ultrasound, Traditional Speech Therapy — NCT03737318.
• Registry record last updated 2026-01-05; status last verified 2025-03.
• Results first posted 2026-01-05.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

The registry describes a completed, randomized, single-masked, parallel-group trial with 108 enrolled participants. The three behavioral groups received traditional articulation treatment, visual-acoustic biofeedback, or ultrasound biofeedback. The primary endpoint measured change in F3-F2 distance for /r/ productions across three treatment sessions in Phase I.

The sponsor reports a linear regression treatment-by-time interaction for the primary endpoint, with a 95% confidence interval and p < .0001. The registry also flags a discrepancy between that analysis and simple recalculations from arm-level summaries; the sponsor’s analysis takes precedence. Two secondary outcomes concern untrained-listener ratings and parent-reported impact, and their sponsor analyses show different statistical patterns.

The record reports zero serious adverse events, other adverse events, and deaths in all three groups. Details about the full statistical plan, missing-data handling, analysis populations, multiplicity, and original sample-size rationale are not reported in the registry record.